Which is a problem, because honestly I’m not sure why I’m not into it. In a field like ecology, where there’s no universal agreement as to what questions are most important to ask or exactly how to go about answering them, I think it becomes more (not less) important that each of us be able to justify our chosen question and approach, in terms that others can appreciate if not necessarily agree with. And also justify not liking any questions or approaches we don’t like. It really bugs me when people object to my own favorite approach for weak reasons that don’t stand up to even casual scrutiny. So I’m embarrassed to admit that there’s lots of trait-based ecology that I just vaguely think of as uninteresting or not likely to go anywhere, even though honestly I don’t know enough about it to really have an informed opinion. It’s embarrassing to not have an informed opinion on what’s probably the most popular current approach to topics that I care a lot about (e.g., species diversity, composition, and coexistence along environmental gradients).

This post is my attempt to do better. I want to think out loud about what I like and don’t like about trait-based ecology. My selfish goal is to clarify my own thinking, and to get comments that will teach me something and help me think better. My less-selfish hope is that buried somewhere within my half-formed thoughts are some useful ideas that trait-based ecology could take on board.

Here’s my plan: I’m going to talk about a body of work in trait-based ecology that I actually do know well and that I do like a lot. Then I’m going to go back to Brian’s old post on where trait-based ecology is at and where it ought to go and see how this body of work stacks up. How do my reasons for liking this particular body of trait-based ecology line up with what an actual trait-based ecologist–Brian–looks for in trait-based ecology?

The body of work I’m going to talk about is from Elena Litchman, Chris Klausmeier, and their group at Michigan State. They’re phytoplankton community ecologists. Which immediately raises the question “What ‘traits’ do unicellular algae have and how on earth does one measure them?” Glad you asked, Imaginary Reader!

For decades, one of the core tools of phytoplankton ecology has been the chemostat: a continuous flow-through culture. Culture medium flows into the culture vessel, and the medium and organisms in it flow out at the same rate:

Chemostat. From nyu.edu.

You grow a population of algae in the culture vessel, vary key aspects of the environment (e.g., the concentration of limiting nutrients in the inflow medium), and measure parameters that describe algal population growth. Those parameters are “traits”, or at least can be thought of as traits (I’ll come back to the issue of whether those parameters are “really” traits). For instance, under constant conditions (meaning: no fluctuations over time in flow rate, the inflow nutrient concentrations, the temperature, etc.), algal per-capita growth rate is an increasing saturating function of the inflow concentration of the limiting nutrient, traditionally denoted by S. That increasing saturating function is described by the Monod model, which can be completely specified by two parameters. The choice of parameters is somewhat arbitrary (there are multiple mathematically-equivalent ways to write the Monod model), but one traditional choice is to use the half-saturation constant Ks (the nutrient concentration at which per-capita growth rate is half its maximum possible value), and the maximum per-capita growth rate μmax:

Illustration of the Monod model, from montana.edu. Per-capita growth rate μ is an increasing saturating function of S, the concentration of the limiting nutrient in the inflow medium.

Those parameters vary interspecifically. For instance, here’s the fit of the Monod model to chemostat data for the growth rate of two algal species as a function of phosphorus concentration in the inflow medium:

Per-capita growth rate of two diatom species as a function of phosphorus concentration in the inflow medium. One species (open circles) has a higher μmax than the other (filled circles). From Steiner et al. 2012.

There are also other traits one can measure in chemostats, such as cellular nutrient quotas (basically, the minimum amount of nutrient X needed to make a new algal cell). Cellular nutrient quotas are parameters in a more complicated growth rate model (the Droop model) one can use to describe algal growth in a chemostat in which flow rate and/or inflow nutrient concentrations vary over time. You also can measure parameters describing growth rate as a function of light levels. You can measure composite parameters like Tilman’s famous R*, the equilibrium level of the limiting resource in a chemostat in which the flow rate and inflow nutrient concentrations are held constant. You can even measure a trait that all you macrobial ecologists would find familiar: body size (i.e. cell size). And one could of course drill down and measure various “low level” physiological, biochemical, and gene expression traits.

But you don’t have to drill down to the underlying physiology and biochemistry when ecologically-relevant effects of those low-level traits are so well-summarized by the “high-level” parameters like μmax, R*, etc. I mean, look at the great fit of the Monod model to the data in that last figure (which is a typical example, by the way)! To which you might reply, pfft, whatever, that’s for a controlled lab environment. There’s no way the laboratory-assayed parameters of the Monod model or the Droop model or etc. will tell us anything about what happens in complex natural environments. Where there are other algal species, and zooplankton, and water turbulence, and evil demons that constantly change the laws of nature just to make life hard for field ecologists.**

You might say that, Imaginary Interlocutor I Invented For Rhetorical Purposes, but you’d be wrong. Elena Litchman, Chris Klausmeier, and their group members have been compiling phytoplankton trait data from the literature. Which leads to several very nice empirical results. First, there are strong cross-species correlations and trade-offs among different parameters:

Three-way trade-off between competitive abilities for N (x-axis) and P (y-axis), and cell size (indicated by size of the circle). The measures of competitive ability are composite parameters reflecting how well species take up N and P, relative to their cellular requirements for N and P. Each point is data for one algal species. Filled circles are freshwater species, open circles are marine species. From Edwards et al. 2011.

Those correlations and trade-offs are interpretable in terms of lower-level physiological and biochemical mechanisms, which is why it’s legit to think of those high-level parameters as “functional traits”. For instance, smaller species are in the upper-right of the above plot (where better nutrient competitors are) and larger species in the lower left because of surface area-volume ratio. The most competitive species for limiting nutrients are the ones with the lowest requirements for those nutrients (i.e. lowest cell volume, all else being equal), relative to their ability to meet their requirements via nutrient uptake through uptake proteins on the cell surface.

Second, many traits are taxonomically or phylogenetically conserved, though of course with substantial variation within groups. So if you see species’ traits as a window into the ultimate evolutionary-historical determinants of current community structure, well, here’s what the view through that window looks like for phytoplankton:

Boxplots of light level at which per-capita growth rate is maximized. Each box summarizes data for species from a different taxonomic group. Modified from Schwaderer et al. 2011.

Third, because the traits for which we have data are the parameters of theoretical models describing population growth, we can use those theoretical models to predict which species with which traits should competitively dominate in which environments. We can then go out into nature and see if species are present or abundant where we’d predict they’d be competitively dominant, and absent or rare where we’d predict them to be outcompeted. This approach famously worked for David Tilman (1977). It still works now that the Litchman-Klausmeier group has compiled data on traits and presence/abundance for many more species in many more lakes. For instance, cyanobacteria do in fact have lower relative abundance in low-light lakes, as you’d predict from their light use traits as compared to the light use traits of other species:

Ok, that’s not the most impressive R^2 ever. But given that we used one laboratory-assayed trait to predict relative abundance in the field, and then just looked at snapshots of relative abundance and a crude measure of light availability to test that prediction, any R^2 significantly >0 is something. Plus, this is just one illustrative example. From Schwaderer et al. 2011.

Anyway, you should totally spend an afternoon reading up on the Litchman-Klausmeier (“LK”) group’s work if you have any interest in trait-based ecology. It’s outstanding work.

But what makes it so outstanding? Why do I love this stuff but not lots of other trait-based stuff? To answer that, I’m going to go back to Brian’s old list of 9 things that trait-based ecology needs to do to fulfill its potential. The LK work does some of them–but also kind of does the opposite of others! My list is numbered to correspond to Brian’s:

1a. LK use an unconventional definition of “trait”. Brian argued that it’s not a functional trait if (i) it’s not something you can measure on an individual organism, and (ii) it’s not linked to individual performance. He complained that too many people are ignoring (i). Well, sorry Brian, but LK’s work ignores (i), and it still works great. The reason being that individual morphology/physiology/biochemistry/gene expression/etc. only matters for species distribution and abundance insofar as it affects per-capita growth rates. If you can summarize the effects of all that low-level morphology/physiology/etc. on per-capita growth rates with a few high-level parameters in a mathematical model, you should totally do it. This is an example of what philosophers of science call “screening off”. If A only causally affects C via its effect on B, you only need to know about B in order to capture A’s effect on C. B is said to “screen off” A’s effect on C. Here, “A” is “cellular biochemistry, etc.”, “B” is “parameters of the Monod or Droop model”, and “C” is “algal abundance under specified environmental conditions”.

1b. LK embrace population ecology rather than trying to avoid it or skip over it. Brian refers to the focus on individual organisms as a “subtle rejection of the population approach”. Which as LK’s work illustrates is maybe one reason why the functional trait bandwagon needs some steering. As discussed in the previous paragraph, LK’s work treats parameters of population growth models as traits! Which seems to me like a really good idea if what you’re ultimately interested in explaining is the distribution and abundance of species. And if those models don’t exactly describe any particular natural system (which they don’t), well, as I just illustrated they still generate testable predictions from which we can learn. And note as well that caring about the parameters of population growth models doesn’t mean not caring about the underlying individual-level morphology/physiology/etc. Chris Klausmeier for one has done some eco-evolutionary modeling of algal physiology and biochemistry to try to explain interspecific variation in population growth parameters. I think one take-home message of LK’s trait-based work for trait-based ecology in general is to quit trying to cut out the “middle man” of population ecology. Quit insisting on always and only trying to go straight from individual-level morphology/physiology/etc. to explanations of distribution and abundance. Instead, go from individual traits to parameters of population ecological models, and from parameters of population ecological models to testable predictions of species’ distributions and abundances.

But really, in saying everything in 1a and 1b, I don’t think I’m saying anything different than what Brian said in his #3: traits are hierarchical, and “higher level” traits covary more with the environment than lower level traits. Which is exactly what one would expect (right?) And which I think is a strong reason to use lower-level traits to explain higher level traits, which then in turn explain abundance. I’m just highlighting that one can and should go to an even higher level than, say, whole-plant carbon use efficiency or whatever. One can go up to the level of parameters in population growth models–Ks values, R* values, etc. in the case of phytoplankton–and still be doing trait-based ecology.

[Aside: There are other examples I could’ve used to illustrate the same points in 1a and 1b. For instance, one can explain a substantial fraction of variation in relative abundance of plant species in N-limited grasslands via their R* values for soil nitrate (Harpole and Tilman 2006). One can of course also explain interspecific variation in R* via interspecific variation in lower-level physiological traits (Craine et al. 2002). I’m not arguing that R* values in particular will always be the high-level traits of interest. It’s just that the best examples that happened to occur to me as I was writing this post all happened to involve R* values.]

2. Embracing variation. LK’s data definitely could be used to look at interspecific trait variation within sites, though as far as I recall they haven’t gone down that road very much yet. They don’t have any data on intraspecific trait variation as far as I know. But I don’t see any obstacle in principle to collecting such data. Just do chemostat trait assays on a bunch of different asexual lines of the same algal species. That would be work, of course, but nobody said ecology was easy.

3. Traits are hierarchical. I talked about this already.

4. Traits aren’t univariate and don’t just reflect 1-D trade-offs. LK’s work is a nice illustration of Brian’s point; see e.g. the 3-D trade-off plot above.

5. Embrace trait x environment interactions. In other words, different traits or trait combinations are best in different environmental contexts. LK’s work is a nice illustration of this point.

6. Theory. As discussed in 1a and 1b above, LK’s work is a powerful illustration of what embracing theory can look like in trait-based ecology. I share Brian’s sense that a lot of trait-based ecology is far removed from theory and that it would really benefit from tighter links with theory. But where I perhaps differ from Brian–and again, this may reflect my own ignorance of much of trait-based ecology–is my sense that the required theory (or at least many of the ingredients for it) already exists in population ecology. Now, embracing theory as they did required LK to take advantage of the accumulated decades of trait measurements by many algal ecologists whose trait measurements have been motivated by the Monod model, the Droop model, etc. LK were lucky that those data were already available (though I’m sure compiling those data was still a lot of work!) But that just illustrates what I’m sure is a familiar point to any trait-based ecologist: you want good trait data for lots of species. Ideally you want data for the traits that theory says are most relevant, rather than for whatever ol’ traits happen to be easiest to measure. If those data don’t exist, you either have to put in the grunt work to collect them, or go work on something else.

This kind of brings up a larger point. My admittedly-vague sense is that one major motivation for a lot of trait-based ecology is a desire for scalability. We want to be able to predict or explain something about any (every!) community. But I get the sense that scalability is somehow supposed to be easy, at least compared to the alternatives. We want a scalable approach that lets us predict or explain every community in one go, because the alternative of studying each community one by one is too much work. LK have scalability in the sense I’ve defined–but only because lots of algal ecologists spent decades doing finicky chemostat assays of theoretically-relevant growth parameters. Being able to work “at scale” in the sense I’ve defined isn’t easy–it often requires a massive up-front investment in data collection.***

7. Individuals. LK only have species-level data, not individual-level data. I already argued that individual-level data isn’t essential for trait-based ecology in general, though there may be specific questions for which it’s essential.

8. Traits besides physiological/morphological traits. LK’s work is a great example of trait-based ecology using traits that are directly relevant for the outcome of species interactions.

9. Traits beyond plants. Phytoplankton are primary producers, but in other ways they’re very different from terrestrial plants. So I’d say LK’s work addresses this need.

So what do you think? Is the LK work a model for trait-based ecology to follow? Good work, but not an example anyone else could emulate? Good work, but far from unique because lots of trait-based ecology already does the same sort of thing just as well? Not really trait-based ecology at all? More broadly, what do you think is the most exciting trait-based ecology being done right now? And are there any popular lines of trait-based research that we could use less of? Really looking forward to your comments.

FYI: I’m going to stay out of the thread for the first few hours to let the conversation develop its own momentum before replying to anyone. I want to take the time to reflect on the first wave of comments and make sure I reply thoughtfully, and I don’t want to dominate the conversation.

Hi Jeremy – thanks for engaging with one of my posts on such a thoughtful level.

First a few points of agreement.

” there’s lots of trait-based ecology that I just vaguely think of as uninteresting or not likely to go anywhere,” I agree. Its why I called trait ecology a bandwagon. Of course that statement doesn’t preclude there being good work in trait ecology. In fact that statement could probably be applied to any field of ecology (including population ecology).

And I completely agree on Elena and Chris’s being a very nice body of work. In fact I highlighted them as one of several examples of successes of a trait-based approach in my comments on my original post. So nothing I am about to say here is a criticism of their work.

And now a couple of points of disagreement (or clarification) – most of which boil down to phytoplankton are not like most things people are studying traits for (macrorganisms like plants and ants and fish).

1) You call the Monod equation a population dynamic equation. And you’re of course technically right since population growth rate is on the y-axis. But it is a much more mechanistically oriented equation than say the logistic or Lotka-Volterra. In fact it can be derived from basic physiological principles. To my mind this puts it about halfway between population dynamics and functional ecology. So by highlighting the Monod equation, you are implicitly acknowledging the critique of phenomenological population dynamics common to those taking a more functional, physiological approach.And thus I would argue these traits are half-way between “population traits” and “functional traits”. Just as a simple example, the Monod equation makes predictions about possible changes due to eutrophication, while a logistic equation version of phytoplankton growth gives no information except about the conditions in which it was parameterized, which makes it circular.

2) A lot of the traits you highlight are measured at the population level only because that is the most convenient level for tiny organisms. In fact this covers most of the traits you mention except for the Monod parameters. Nutrient use efficiencies (Cn, Cp), cell size, and optimal insolation rates all have direct analogs as some of the most commonly measured traits in the plant world. The only difference is in the plant world, the plants are close enough to our human scale that our instruments can measure them on a single plant (or a single leaf), whereas in phytoplankton they are much more easily measured on a bottle (but could in theory if we cared enough measure them on a single cell). So this is really a scale difference based on organism size, not a philosophical difference.

3) In my original post I cited the phytoplankton body of work as one of several examples of interesting trait work. So to take your litmus test example of predicting relative abundance by secchi depth (via Iopt), Shipley 2006 and Laughlin 2012 both predict relative abundances using traits sensu strictu (i.e. physiological traits measured on individuals) with R2 *way* better than the example you give. This suggests to me that you might like traits if you read some of the other good papers (admittedly buried amidst a lot of more descriptive papers).

As usual, I think we agree more than we disagree, but its more fun (informative?) to focus on the areas of disagreement.

I agree with all of this, though I’d put some of it slightly differently.

On a minor point, I’m curious to hear more of your thoughts on Shipley (2006). My reaction to that paper was that it was exceptionally creative but that the approach doesn’t work for technical reasons that commenters on the paper pointed out (IIRC: if you impose too many ‘constraints’ in MaxEnt you make it impossible for the observed data to deviate from the MaxEnt prediction, even if those constraints are completely arbitrary). It’s not clear to me that Shipley’s follow-up papers fully address those technical issues or not. You’ve clearly looked at this stuff closely so I’d be interested to hear your view.

On the Shipley paper – I never quite bought the constraints. There were a lot of degrees of freedom remaining. Probably the bigger issue is the fit is very good on an arithmetic (untransformed abundance) but not too good on a log-log plot (i.e. log transformed abundances). But then you can say that about a lot of predictions of abundance (predicting an abundance of 1.5 vs 1.1 is harder than an abundance of 10 vs 1 but there are a lot of species with low abundances). Shipley also introduces one of the few mechanistic models of environmental filtering to justify maxent. I still think it is a worth reading. As is the Laughlin & Laughlin 2013 paper that compares Laughlin 2012 traitnet approach with the 2006 Shipley MaxEnt approach.

I agree that mechanistic models of how population growth depends on traits and environments, and feed back on the environment, are a missing link in much of trait-based ecology. Those are relatively easily supplied for plankton (which is one reason why we study them). But it should be possible for other organisms too. Daniel Falster & colleagues’ recent PNAS paper on forests and Ken Haste Andersen’s work on size-structured fish communities are two applications of the same conceptual approach to more complex communities that come to mind.

Once those system-specific models have been made, we have plenty of trait-based modeling frameworks to look at community assembly and eco-evo dynamics, such as optimization theory, adaptive dynamics and quantitative genetics.

“I agree that mechanistic models of how population growth depends on traits and environments, and feed back on the environment, are a missing link in much of trait-based ecology. ”

Yup. The shorter version of much of this post is “trait-based ecology is not going to be able to get very far totally ignoring density- and frequency-dependence” (i.e. ignoring those “feedbacks on the environment” to which you refer).

“Once those system-specific models have been made,”

This is an important point I wish I’d made in the post. That’s a strength of your group’s work: it’s based in a system-specific model. As opposed to model-independent attempts to, say, measure “functional diversity” and how it affects or is affected by other things.

And let me acknowledge some of those former students & postdocs who’ve actually done most of this work: Kyle Edwards (now an assistant professor at Hawaii), Mridul Thomas (now a postdoc at EAWAG and soon to start at the Danish Technical University), Colin Kremer (back as our ghost-doc), Beth Miller (now a postdoc at Oregon), and a host of others!

Jeremy, I can understand your lack of excitement about trait-based ecology. You captured the heart of the problem by trying to understand what constitute a trait. Little was done in a lot of cases to justify the ecological relevance of many of the so-called functional traits. At the same time, I think you misunderstood Brian’s (he can correct me if I’m wrong) view of a functional trait, which is less in the context of population growth but more like the way evolutionary biologists would view a trait—in the context of fitness. But many authors of the trait-based studies did not work from this perspective, which kind of justify your view in some sense.

In the same vein, population ecologists are focusing on resource-based response, which may not reveal much about the biological basis for any given response. But this is what the folks working on trait-based ecology are interested in. Candidly, I’m not surprised by many of the findings of population growth experiments involving nutrient variation because we know about phenomena such as resource partitioning since the 80s and the fact that resource consumption scales with organism’s body mass. Understanding the ecophysiological basis for the difference in response between populations would be an interesting direction, which I don’t think fitting growth models can solve.

An appeal of the trait-based ecology is that it has the potential to address whether traits influence distribution (not coexistence). For example, we know that plant distributions are influenced by climate, but what determines distribution within a given climate space after accounting for factors like barrier to dispersal, edaphic preferences etc? If we can understand this, a lot of other areas of interest (e.g. coexistence) may be better understood.

I would agree with Tobi’s points. Including the fairly important point Tobi articulated better than I have that if you want to get to species differences and how they matter across environmental gradients, traits have a lot of promise. Not sure population ecology has as much promise. Indeed, there are not even a lot of attempts outside of some papers on temperature and population dynamics (Yodzis/McCann/Vasseur & yes Fox and its probably not a coincidence that those are two interwove academic lineages).

I think Tobi put the contrast of a fitness trait vs a population dynamic trait well too (in our 2006 TREE paper we often talked about fitness but only wrote “performance” because we knew fitness was a technical morass we didn’t want to get into).

Thanks for your comments. I confess I find some of them a bit puzzling, which probably just illustrates that I’m not a trait-based ecologist.

I don’t understand the distinction between fitness in the sense an evolutionary biologist might understand that term and population growth rate. Mean absolute fitness and per-capita growth rate are one and the same thing for many purposes. Roughly, they both are the average contribution of a member of the current generation to the next generation. Right? That’s why, in his comment above, Chris Klausmeier (“lowendtheory”) refers to “optimization theory, adaptive dynamics, and quantitative genetics” as tools to look at community assembly and eco-evolutionary dynamics.

“An appeal of the trait-based ecology is that it has the potential to address whether traits influence distribution (not coexistence). ”

Hmm…except that biotic interactions influence distribution, right? I mean, distribution and coexistence aren’t two different, unrelated things. And if you say that distribution is about coarse spatial grains and biotic interactions only affect coexistence at fine grains, I’d say you’re wrong, because what happens at coarse grains is just the aggregate outcome of what happens at fine grains. William Godsoe’s recent work is good on this point. And isn’t a lot of mechanistic “niche” modeling these days moving in the direction of incorporating species interactions more explicitly?

@Jeremy, Brian predicted quite correctly that using a field-specific terminology might generate an unintended argument. For simplicity, let’s consider a trait as something that has a functional relevance—mediate growth, reproduction, survival, etc.

“Mean absolute fitness and per-capita growth rate are one and the same thing for many purposes. Roughly, they both are the average contribution of a member of the current generation to the next generation. Right?”

This is correct to some degree but in my view, evolutionary biologists are more interested biological details. They look at individuals within a population and the characters influencing their fitness and whether these characters can evolve—typically under some sort to selective pressure. Less about number of individuals within a population. The closest analogy that I can think of is like finding out that global poverty has declined despite increase in global population. You might need to look at the regional data to know what that means—looking at regional data can be considered the territory of evolutionary biologists in this analogy.

“except that biotic interactions influence distribution, right? I mean, distribution and coexistence aren’t two different, unrelated things. And if you say that distribution is about coarse spatial grains and biotic interactions only affect coexistence at fine grains, I’d say you’re wrong, because what happens at coarse grains is just the aggregate outcome of what happens at fine grains…And isn’t a lot of mechanistic “niche” modeling these days moving in the direction of incorporating species interactions more explicitly?”

Excluding coexistence was an attempt not to get into one of those old debates. I used to hold similar view as you about plant distribution until I had the privilege of working on two distinct systems—rock barrens and Sphagnum peatlands—that gave me something to think about. For instance, Sphagnum moss distribution within a peatland are determined by microtopography that represents a profile of wetness and the position of a species along the profile is an indication of the species’ water economy. What’s more? These species are highly clonal and do not compete (inter or intra) for most resources but share them. From modelling perspective, this is a very easy system to model (which I have done) because you can easily incorporate coexistence. However, you will never be able to use those niche models (or coexistence hypothesis) to explain why globally you will have the same section of a given moss genus occupying a relatively the same position along 40cm or so microtopographic profile. This is the kind of question that folks working on trait-based ecology are trying to ask. Growth and niche models are useless in this context.

Of course technically 1/N dN/dt is fitness. But (agreeing with Tobi) it is a question of emphasis. Population biology really cares about the absolute number so they can predict N next year. Evolution (and traits) really care about relative fitness (I use this meaning just rank order -not the normalized by average fitness but still quantitatively precise sense of evolution). They really want to know how do traits varying across species cause the relative performance of those species to vary in a specific environment or across a range of environments. Thus, it is common to focus on a “component of fitness” in evolution, but not in population dynamics.

And it is also common to directly measure a component of fitness (as a proxy for 1/n dn/dt) but in population ecology the absolute value of 1/n dn/dt is so important to keep things calibrated rather than just relative that it essentially has to be derived from fitting a population dynamic equation

Jeremy wrote:
“I don’t understand the distinction between fitness in the sense an evolutionary biologist might understand that term and population growth rate. Mean absolute fitness and per-capita growth rate are one and the same thing for many purposes. Roughly, they both are the average contribution of a member of the current generation to the next generation. Right?”
That summarizes what I thought, too. I wonder if those of us who work on little things that grow quickly (Elena, Chris, Jeremy, and myself included in that group) tend to view them as more synonymous?

I’m sure that’s true. Its pretty boring (in fact deadly) trying to hang around to assess the fitness of a tree or a desert tortoise.

But I do think like Mark also highlighted there is an aspect of goal too. Trait views are about comparing across many species. Fitness/population views are typically about one or a few species across time.

Also, I think its important to be clear about how you measure a field. I’m not surprised that the majority or seeming overall body of trait papers are unexciting to you, Jeremy. The majority of papers in any field are unexciting to people outside that field. I think for an outsider to get the true measure of a field, you have to look at the top 10% papers. Should I judge population ecology by the 100s of papers measuring the mortality rate of a deer population in Connecticutt (important for conservation though), or by the rarer cool papers by Fox, Brian Dennis, Jim Cushing, Kimball etc? And in which case, how many of those papers in trait ecology have you read? We both agree on liking the Litchman/Klausmeier papers a lot.

“I think for an outsider to get the true measure of a field, you have to look at the top 10% papers.”

Oh, I agree completely!

“And in which case, how many of those papers in trait ecology have you read?”

Well, that’s the thing–I’m not sure! I find it difficult to define the boundaries of “trait-based ecology”, to an even greater extent than for the boundaries of other large subjects that bleed into others (community ecology, say, or biodiversity-ecosystem function work). I don’t *think* I’m alone in this: I recall Meghan reading your old post and going “huh, I guess I do trait-based ecology?” So if Meghan’s stuff counts as “trait-based ecology”, I’ve read Meghan’s stuff! 🙂 And I’ve read my own paper with Stan Harpole suggesting a way to incorporate species’ traits into the Price equation and use it to partition BEF relationships. Except that in that paper, we quite openly define “trait” as “a number attached to a species”. So that traits for our purposes could include not just, e.g., body size or even R* values, but things like geographic range size or the number of consumer species that eat the focal species. So I guess my semi-serious question is, where does “trait based” ecology stop and “ecology based on any ol’ numbers” start?

I suppose one answer would be “it’s not *really* a ‘trait’ if its value is too context dependent”. A trait is supposed to be an attribute of an individual organism (or maybe, the average attribute of all adult members of that species). If the trait is too context-dependent (perhaps because it depends on the individual organism’s attributes only very indirectly, and/or depends on lots of other things too), it ceases to be very useful to think of it as an attribute of the individual organism. Kind of like how “extended phenotype” thinking gets silly if taken too far. But then again, how much context dependence is too much? After all, most phenotypic traits are plastic to some degree.

Anyway, I’ll tell you some trait-based stuff I’ve read or skimmed and what I think of it. You tell me if it actually counts as “trait-based”, what you think of it, and what major chunks of trait-based stuff I’ve just totally overlooked.

-Old stuff from the zooplankton ecology literature on how zooplankton body size and other attributes (e.g., range of particle sizes that can be ingested) relate to competitive outcomes. Stuff from folks like Gliwicz

-Stuff from Jon Levine’s group (using terrestrial plants) and Brad Cardinale’s group (using algae) doing lots of pairwise mutual invasibility experiments to see which species can coexist stably, and then also measuring lots of traits of those species to see how trait differences and similarities map onto ability to coexist (“they don’t, at least not in any simple or easily interpretable way” seems to be the answer). Some of this work also tries to use phylogenetic relatedness as a proxy for “overall” phenotypic similarity, finding that phylogenetic relatedness mostly sucks as a predictor of competitive outcomes. I really like this work, although I think part of its value is in throwing cold water on some ideas that I don’t think should ever have gotten to the point where they needed to have cold water thrown on them.

-Stan Harpole’s work using R* values to predict terrestrial grassland plant abundances both near the sites where the R* values were originally measured, and at sites far away. Very nice work.

-Jon Shurin’s group’s work measuring algal traits in chemostats and using those trait data to interpret studies of overyielding and biofuel production.

-Lots of descriptive studies of “functional diversity”, both as a predictor variable and a response variable. How functional diversity in this or that taxonomic group or assemblage varies along environmental gradients, or with spatial grain, or with the functional diversity of some other group. Whether functional diversity or species richness better predicts primary productivity or some other ecosystem function. How an experimental manipulation of X indirectly affected the functional diversity of assemblage Y (e.g., how does manipulating aboveground herbivory on plants affect the functional diversity of soil microbes?). I find most all of this work boring, for various reasons. Which worries me because there’s a *lot* of it, so I worry that in not liking this stuff I’m just being narrow-minded or over-critical, or just expressing a mere personal preference (like preferring beer to wine).

-Associated with said descriptive studies: lots of methods papers about the properties of different measures of “functional diversity” (e.g., dendrogram-based vs. not). Those methods papers all seem kind of pointless to me because there’s no way to define “functional diversity” sufficiently precisely to make it measurable in the way that, say, mass or temperature is measurable.

-I’m vaguely aware of huge chunks of stuff I haven’t read. Leaf economics spectrum stuff, for instance. I’m aware that the causes and consequences of the leaf economics spectrum are both huge important topics in trait-based ecology, but I’m pretty much ignorant of them.

p.s. It occurs to me that there’s a potentially-interesting follow-up post here. Within any sufficiently-large body of work on any topic, there will be some work that also becomes well-known to people who don’t work on that topic themselves. Is that work usually the “best” work on the topic, as judged by specialists? If not, why not? And what happens if the view of the specialists changes over time, while the view of the non-specialists doesn’t? Conversely, there are some topics on which even the “best” work, as judged by specialists, is unknown to non-specialists. Why is that? Is it just a matter of luck–purely arbitrary fads? Or is it a bad sign for all work on a topic if even the best (most important, most interesting) work on that topic, as judged by specialists, is seen as boring or unimportant by non-specialists?

I would say all of the stuff you list is trait ecology, and mostly good trait ecology, but (with the possible exception of functional diversity) is not “mainstream” trait ecology. A lot of your trait reading seems centered on how traits affect competitive interaction outcomes which I think mainstream trait literature is ignoring to its detriment. To broadly oversimplify a lot of mainstream trait literature is focused on trait-tradeoffs (like the leaf economic spectrum) and trait environment correlations. In the end traits are just the ecologists version of phenotype (focus on phenotype vs environment instead of evolution of phenotype – and yes the only distinction between those two is a matter of emphasis).

Re: trait-environment correlations, what’s the best theory on this on your view? And does any of that theory ask whether/how density- and frequency-dependent species interactions will affect trait-environment relationships? And is all of that theory system specific, or have people also asked about trait-environment relationships in the context of “toy” models? I ask because I have a little toy model paper on the closely-related question of trait-abundance relationships within a single site (https://www.nature.com/nature/journal/v238/n5364/abs/238413a0.html).

The theory on this of which I’m aware is metacommunity models. You have sites distributed along some environmental gradient, and a bunch of species that can potentially occupy those sites, and your model makes assumptions about how those species move around and interact with one another. Michel Loreau has done these sorts of models. Andy Gonzalez, Mathew Leibold, Peter Abrams, others…But that stuff wouldn’t really qualify as “trait-based” if we’re focusing on “mainstream” traits like the leaf economic spectrum. It would qualify as “trait-based” if quantities like R* and P* values count as “traits”.

There is not a lot of trait-environment theory at the moment. Most of it is correlation of observational data. The Laughlin & Shipley papers I mentioned are the best theory to date. The metacommunity theory that I’ve seen usually just assumes you have species with different levels of fit to different environments (e.g. gaussian fitness along a 1-dimensional environmental gradient). So fit to environment is just a randomly generated property of species. I don’t see traits there. I think it is fair to say the trait world is more interested in unpacking what traits (and processes) cause that varying fit to environment.

Thanks for an interesting post Jeremy! I agree that trait-environment relationships remain under-theorized. However, one exciting avenue for this theory emerges from invoking adaptive dynamics/eco-evolutionary modeling. In brief, if you can assemble a reasonable model of how ‘fitness’ (as per capita growth rate…) depends on species’ traits and their environment, you can use these approaches to predict which trait(s) optimize the fitness of one or more species in that environment. Repeat the process across hypothetical or realistic environmental gradients (exploring parameter space), and you can begin to assemble theory for trait-environment relationships.

We used this approach to understand & predict relationships between the optimum temperature trait of phytoplankton and their local thermal environments (Thomas et al. 2012). Or, cell size can be predicted based on the frequency of nutrient pulses (Litchman et al. 2009). Spatial structure, gene flow, and dispersal can be incorporated as well (Norberg et al. 2012). I think there are many exciting – and untapped – opportunities for connecting eco-evolutionary theory (which all too often remains within a theory bubble) with real-world relationships, using traits as the connection.

Good post & great comments! I haven’t read the LK work, but have read Brian’s previous posts on traits and really enjoyed them. I think there is a lot of interesting trait-based work being done now linking species/communities with ecosystem function & services, esp insects in agroecosystems – this is what I work on, so I mostly follow this subset of trait literature. I think the trait linkage framework is a really neat way of linking species & communities with environmental change and changes in function and has lots of opportunities for interesting work. It was initially developed on plants (Katherine Suding, Sandra Lavorel et al), but also recently applied to vertebrates (Gary Luck (my previous advisor) et al). I also think it would also be interesting to look back at some of the old work on biometry from the late 1800s, I imagine there would be some interesting parallels.

Hi Manu – thanks for bringing up the topic of how traits affect ecosystem function. I tend not to focus on it because it is not my primary interest. But it is for sure a major root of the interest in traits.

If you try to figure out what trait ecology is just working from the meaning of the word “trait”, then it’s pretty much the whole of ecology. Physiological ecol and functional ecol are obviously about traits. Evolutionary ecology is too. Ecosystem ecology and community ecology also (with exception of neutral theory maybe) – hard to see how you can say anything useful about ecosystem processes or species interactions without talking about traits. So what does it even mean to say “trait ecology”?

For me it makes most sense to think about it historically. It emerged from arguments about ecological strategies in land plants. The most promising strategy ideas up to mid-1990s lay in CSR theory. But how to attribute ratings on (say) a C-S scale to species, in a way that allowed species from different continents to be compared? At first this seemed like a problem of using measurable traits to calculate “stress-tolerance” or “ruderality”. But then the suggestion was made to set the concepts aside for a while, just use traits directly as the dimensions for comparing species, and discuss afterwards what the scattergram meant in strategy terms. And that approach caught on.

So this achieved a couple of things. First and most obviously, it has made possible lots of comparison – dozens of papers over past 20 years looking at traits and trait constellations, across all continents and across the whole of vascular plants – a really substantial scaling-up from the comparisons across six Banksia species or five Solidago species that went before.

It’s worth noting that one shouldn’t see these scaled-up comparisons as a new type of ecology occurring all by themselves. Mechanistic understanding of the trade-offs, and detailed work across smaller numbers of species, are surely still central. But the wider comparisons across many species using easier-to-measure traits make a productive complement to that more intensive work.

A second thing achieved by the past 20 years, in context of ecosystem and community ecology, is renewed interest in species traits relative to species diversity. From early 1970s species diversity had become the touchstone for whether we understood what was happening in a community. (And beginning from MacArthur-Levins through the seminal textbooks of early 1970s, this indeed seemed to make sense at first.) But looking back over 1970-2010, doesn’t it seem fairly peculiar that most community theory was so focused on explaining diversity, without hardly addressing at all what the species were actually like? – how tall they were, or what their leaf N content was? One effect of “trait ecology” has been to bring attention back to the question what sort of species occur in communities.

So in summary, for me trait ecology is best understood as a code-phrase for a particular sort of activity over the past 20 years, making really broad comparisons across species using whatever traits seem gettable and enlightening.

I expect the fashion for “trait ecology” is almost over now. Not in the sense that we’ll stop working on traits, but in the sense that working on traits is so obviously integral to all kinds of ecology that we’ll stop trying to distinguish trait ecology from other sorts of ecology.

One thing that trait-based ecology critiques, as Mark articulates nicely above, is the pursuit of understanding biodiversity for the sake of diversity itself, without connection to the relevant properties of species – an important critique. However, as enthusiasm for trait approaches grows, there’s a risky tendency that we end up engaging in measuring traits for measurement’s sake. If all trait-based ecology does is add a larger list of attributes to each species, in addition to its name, perhaps we’ve just kicked the can down the road.

Despite being a trait-enthusiast, I think the enterprise of understanding the ecology of a meaningful fraction of species across communities based on determining and measuring their important traits is daunting. At a basic level, the sheer amount of measurements required is potentially enormous (especially considering trait-environment relationships, intraspecific variability, etc., etc., see Brian’s previous post, or Kremer et al. 2016 – http://onlinelibrary.wiley.com/doi/10.1002/lno.10392/full ).

Consequently, I think the key to productively pursuing trait approaches is to pay very careful attention to situations where traits allow us to achieve simplifications. For example, if we want to understand ecosystem function in a given environment (or across the planet!), maybe we can make a lot of progress by predicting the likely traits (or functions) of a few dominant species… even if we can’t say for sure what the identity of these species is in any specific location. These are the kinds of patterns that may be revealed by the broad comparisons Mark mentions. While some aspects of trait ecology might best be left to go out of fashion, hopefully the focus on using traits to simplify/clarify ecology remains.

“However, as enthusiasm for trait approaches grows, there’s a risky tendency that we end up engaging in measuring traits for measurement’s sake. If all trait-based ecology does is add a larger list of attributes to each species, in addition to its name, perhaps we’ve just kicked the can down the road. ”

I completely agree with this. It’s why I don’t like most papers about “functional diversity”. I don’t care what algorithm you used to turn your trait matrix into a diversity measure. Just boiling down a bunch of phenotypic measurements into a diversity index and then looking at how that measure correlates with some other variable is not useful. Not even if all the phenotypic traits you measured are “functional”.

Mark Westobys last paragraph has an important point, that traits are used in all kinds of ecology and I would not really consider it something “stand-alone”.
In plant-insect and plant-plant interaction studies using trait to investigate why certain interactions occur and other not or how plant ensure pollination or avoid herbivory provide amazing insights.
The work on plant-plant communication, herbivory and plant/root volatiles of e.g. R. Karban or Ted Turling. Trait (mis-)match in plant-pollinator interactions or the importance of plant volatiles to attract mutualists or avoid antagonists and in the end ensure reproduction (by a lot of different people). Usually plant volatiles, floral morphology or resources are all named as traits and thus this could be also considered trait-based ecology.

I think that development of “trait ecology” is similar to that of “network ecology”. At the beginning most network paper looked at network structure and how this changed over environmental gradients or something else and reported some indices. But over the years, networks become “just” a tool to investigate questions in all kind of areas of ecology. Thus, network ecology moved away from doing network ecology for its own sake similar as trait-based ecology will move away from reporting functional diversity for the sake of functional diversity. Additionally, the phrase network ecology become less and less used over the years. However, this is just my impression and not based on any valid data or so.

He was a microcosmologist, which I am as well. I was amused by the thought that we microcosmologists might somehow be able to go out and give the field ecologists even more uncontrolled variability to deal with.

Must have to do with functional traits of demons.
So, what’s with demons being invoked in ecological literature? Can we blame it on Stuart Hurlbert for suggesting for human sacrifice to exorcise ecological field experiments of demonic intrusions? (And I wonder how many of the thousands of people citing his pseudoreplication paper actually read it far enough to find this troubleshooting suggestion?).
Or before that, Ronald Fisher reportedly was plagued by demons in the form of school girls whose headmaster decided that weeding a farm field near the school would be a good way to build character and physical fitness. However the farm field was part of the Rothamsted experimental station and it took Fisher some time to figure out why yields from that particular experimental unit were consistently anomalous.
Microcosmologists, school girls, and other scary demons. Anyone know witches or wizards made appearance in the ecology literature, or just demons?

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